NBER WORKING PAPER SERIES

SELL LOW AND BUY HIGH:ARBITRAGE AND LOCAL PRICE EFFECTS IN KENYAN MARKETS

Marshall BurkeLauren Falcao Bergquist

Edward Miguel

Working Paper 24476http://www.nber.org/papers/w24476

NATIONAL BUREAU OF ECONOMIC RESEARCH1050 Massachusetts Avenue

Cambridge, MA 02138April 2018

We thank Christopher Barrett, Kyle Emerick, Marcel Fafchamps, Susan Godlonton, Kelsey Jack, Jeremy Magruder, Nicholas Minot, and Dean Yang for useful discussions, and thank seminar participants at ASSA, BREAD, CSAE, IFPRI, Kellogg, Michigan, NEUDC, Northwestern, Stanford, PacDev, UC Berkeley, and the University of Chicago for useful comments. We also thank Peter LeFrancois, Ben Wekesa, and Innovations for Poverty Action for excellent research assistance in the field, and One Acre Fund for partnering with us in the intervention. We gratefully acknowledge funding from the Agricultural Technology Adoption Initiative and an anonymous donor. All errors are our own. The views expressed herein are those of the authors and do not necessarily reflect the views of the National Bureau of Economic Research.

NBER working papers are circulated for discussion and comment purposes. They have not been peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies official NBER publications.

© 2018 by Marshall Burke, Lauren Falcao Bergquist, and Edward Miguel. All rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted without explicit permission provided that full credit, including © notice, is given to the source.

Sell Low and Buy High: Arbitrage and Local Price Effects in Kenyan MarketsMarshall Burke, Lauren Falcao Bergquist, and Edward MiguelNBER Working Paper No. 24476April 2018JEL No. D21,D51,G21,O13,O16,Q12

ABSTRACT

Large and regular seasonal price fluctuations in local grain markets appear to offer African farmers substantial inter-temporal arbitrage opportunities, but these opportunities remain largely unexploited: small-scale farmers are commonly observed to "sell low and buy high" rather than the reverse. In a field experiment in Kenya, we show that credit market imperfections limit farmers' abilities to move grain inter-temporally. Providing timely access to credit allows farmers to buy at lower prices and sell at higher prices, increasing farm revenues and generating a return on investment of 28%. To understand general equilibrium effects of these changes in behavior, we vary the density of loan offers across locations. We document significant effects of the credit intervention on seasonal price fluctuations in local grain markets, and show that these GE effects shape individual level profitability estimates. In contrast to existing experimental work, the results indicate a setting in which microcredit can improve firm profitability, and suggest that GE effects can substantially shape microcredit's effectiveness. In particular, failure to consider these GE effects could lead to underestimates of the social welfare benefits of microcredit interventions.

Marshall BurkeDepartment of Earth System ScienceStanford UniversityStanford, CA 94305and NBERmburke@stanford.edu

Lauren Falcao BergquistBecker Friedman Institute1126 E. 59th StreetSHFE 214Chicago, IL 60637lfbergquist@uchicago.edu

Edward MiguelDepartment of EconomicsUniversity of California, Berkeley530 Evans Hall #3880Berkeley, CA 94720and NBERemiguel@econ.berkeley.edu

A randomized controlled trials registry entry is available at https://www.socialscienceregistry.org/trials/67

A supplementary appendix is available at http://www.nber.org/data-appendix/w24476

1 Introduction

African agricultural markets are thin and imperfectly integrated, resulting in substantial variation

in staple commodity availability and prices (Fafchamps, 1992; Barrett and Dorosh, 1996; Minten

and Kyle, 1999). Particularly pronounced are price fluctuations seen over time, with grain prices

in major markets regularly rising by 25-40% between the harvest and lean seasons, and often more

than 50% in more isolated markets. Underpinning these fluctuations is seemingly puzzling behavior

at the farmer level: despite having access to relatively cheap storage technologies, farmers tend to

sell their crops immediately after harvest and, in many areas, then later return to the market as

consumers several months later in the lean season once prices have risen.

In this paper, we explore the role of financial market imperfections in contributing to farmers’

apparent inability to exploit this arbitrage opportunity. Lack of access to credit markets has long

been considered to play a central role in underdevelopment, but much of the literature has focused

on the implications for firm growth and occupational choice (Banerjee and Newman, 1993; Galor and

Zeira, 1993; Banerjee and Duflo, 2010). Here, we explore a novel channel by which poor financial

market access may limit development: by restricting individuals’ ability to engage in arbitrage

and, at a macro level, by subsequently contributing to the large seasonal price fluctuations that

characterize these markets.

Rural households’ difficulty in using storage to move grain from times of low prices to times

of high prices appears at least in part due to limited borrowing opportunities: lacking access to

credit or savings, farmers report selling their grain at low post-harvest prices to meet urgent cash

needs (e.g., to pay school fees). To meet consumption needs later in the year, many then end up

buying back grain from the market a few months after selling it, in effect using the maize market

as a high-interest lender of last resort (Stephens and Barrett, 2011).

Working with a local agricultural microfinance NGO, we offer randomly selected smallholder

maize farmers a loan at harvest, and study whether access to this loan improves their ability to

use storage to arbitrage local price fluctuations relative to a control group. We find that farmers

offered this harvest-time loan sell significantly less and purchase significantly more maize in the

period immediately following harvest, and this pattern reverses during the period of higher prices 6-

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9 months later. This change in their marketing behavior results in a statistically significant increase

in revenues (net of loan interest) of 545 Ksh (or roughly 6 USD), suggesting that the loan produces

a return on investment of 28% over a roughly nine month period. We replicate the experiment in

two back-to-back years to test the robustness of these results and find remarkably similar results

on primary outcomes in both years.

We also run a long-run follow-up survey with respondents 1-2 years after harvest-time credit

intervention had been discontinued by the NGO, to test whether farmers are able to use the

additional revenues earned from this loan product to “save their way out” of credit constraints

in future years. We find no evidence of sustained shifts in the timing of farm sales in subsequent

seasons, nor do we see long-run effects on sales or revenues in subsequent years.1

To explore whether this shift in sales behavior by individuals farmers has an effect on market-

level prices, we experimentally vary the density of treated farmers across locations and tracked

market prices at 52 local market points. We find that increase grain storage at the market level

(induced by the credit intervention) led to significantly higher prices immediately after harvest and

to lower (albeit not significantly so) prices during the lean season. One immediate implication of

these observed price effects is that grain markets in the study region are highly fragmented.

We find that these general equilibrium effects also greatly alter the profitability of the loan.

By dampening the arbitrage opportunity posed by seasonal price fluctuations, treated individuals

in areas highly saturated with loans show diminished revenue gains relative to farmers in lower

saturation areas. We find that while treated farmers in high-saturation areas store significantly

more than their control counterparts, doing so is not significantly more profitable; the reduction

in seasonal price dispersion in these areas may reduce the benefits of loan adoption. In contrast,

treated farmers in low-density areas have both significantly higher inventories and significantly

higher profits relative to control.

These general equilibrium effects — and their impact on loan profitability at the individual

level — have lessons for both policy and research. In terms of policy, the general equilibrium

effects shape the distribution of the welfare gains of the harvest-time loan: while recipients gain

1Though we do find some evidence of heterogeneity by treatment saturation.

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relatively less than they would in the absence of such effects, we find suggestive evidence that non-

recipients benefit from smoother prices, even though their storage behavior remains unchanged.

Though estimated effects on non-treated individuals are relatively imprecisely estimates, a welfare

calculation taking the point estimates at face-value suggests that 69% of overall gains in high-

treatment-intensity areas accrue to program non-recipients. These gains to non-recipients, which

cannot be readily recouped by private sector lending institutions, may provide some incentive for

public provision of such products.

The eroding profitability of arbitrage that we observe in highly loan saturated areas also has

implications for impact evaluation in the context of highly fragmented markets, such as the rural

markets in this study. When general equilibrium effects are pronounced and the SUTVA assumption

violated (Rubin 1986), the evaluation of an individually-randomized loan product may conclude

there is a null effect even when there are large positive social welfare impacts. While this issue

may be particularly salient in our context of a loan explicitly designed to enable arbitrage, it

is by no means unique to our setting. Any enterprise operating in a small, localized market or

in a concentrated industry may face price responses to shifts in own supply, and credit-induced

expansion may therefore be less profitable than it would be in a more integrated market or in

a less concentrated industry. Proper measurement of these impacts requires a study design with

exogenous variation in treatment density.

The results speak to a large literature on microfinance, which finds remarkably heterogenous

impacts of expanded credit access. Experimental evaluations have generally found that small

enterprises randomly provided access to traditional microfinance products are subsequently no

more productive on average than the control group, but that subsets of recipients often appear to

benefit.2

Here we study a unique microcredit product designed to improve the profitability of small

farms, a setting that has been largely outside the focus of the experimental literature on credit

2Experimental evaluations of microcredit include Attanasio et al. (2011); Crepon et al. (2011); Karlan and Zinman(2011); Banerjee et al. (2013); Angelucci et al. (2013) among others. See Banerjee (2013) and Karlan and Morduch(2009) for nice recent reviews of these literatures. A related literature on providing cash grants to households andsmall firms suggest high rates of return to capital in some settings but not in others. Studies finding high returns tocash grants include De Mel et al. (2008); McKenzie and Woodruff (2008); Fafchamps et al. (2013); Blattman et al.(2014). Studies finding much more limited returns include Berge et al. (2011) and Karlan et al. (2012).

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constraints. Why do we find positive effects on firm profitability when many other experimental

studies on microcredit do not? First, unlike most of the settings examined in the literature, using

credit to “free up” storage for price arbitrage is a nearly universally available investment opportunity

that does not depend on entrepreneurial skill.3 Farmers do not even have to sell grain to benefit

from credit in this context: a net-purchasing farm household facing similar seasonal cash constraints

could use credit and storage to move its purchases from times of high prices to times of lower prices.

Second, the terms of repayment on the loan we study are flexible, which has been showing to be

important for encouraging investment (Field et al., 2012). Finally, as described above, the general

equilibrium effects of credit expansion could alter individual-level treatment effect estimates in a

number of ways, potentially shaping outcomes for both treated and untreated individuals (Breza

and Kinnan, 2018)). This is a recognized but unresolved problem in the experimental literature

on credit, and few experimental studies have been explicitly designed to quantify the magnitude of

these general equilibrium effects (Acemoglu, 2010; Karlan et al., 2012).4 Our results suggest that,

at least in our rural setting, treatment density matters and market-level spillovers can substantially

shape individual-level treatment effect estimates.5

Beyond contributing to the experimental literature on microcredit, our paper is closest to a

number of recent papers that examine the role of borrowing constraints in households’ storage

decisions and seasonal consumption patterns.6 Using secondary data from Kenya, Stephens and

3Existing studies have concluded that many small businesses or potential micro-entrepreneurs simply might notpossess profitable investment opportunities (Banerjee et al., 2013; Fafchamps et al., 2013; Karlan et al., 2012; Banerjee,2013) or may lack the managerial skill or ability to channel capital towards these investments (Berge et al., 2011;Bruhn et al., 2012).

4For instance, Karlan et al. (2012) conclude by stating, “Few if any studies have satisfactorily tackled the im-pact of improving one set of firms’ performance on general equilibrium outcomes. . . . This is a gaping hole in theentrepreneurship development literature.” Indeed, positive spillovers could explain some of the difference betweenthe experimental findings on credit, which suggest limited effects, and the estimates from larger-scale natural exper-iments, which tend to find positive effects of credit expansion on productivity – e.g. Kaboski and Townsend (2012).Acemoglu (2010) uses the literature on credit market imperfections to highlight the understudied potential role ofGE effects in broad questions of interest to development economists.

5Whether these GE effects also influenced estimated treatment effects in the more urban settings examined inmany previous studies is unknown, although there is some evidence that spillovers do matter for microenterpriseswho directly compete for a limited supply of inputs to production. For example, see De Mel et al. (2008) and theirdiscussion of returns to capital for bamboo sector firms, which must compete over a limited supply of bamboo. Inany case, our results suggest that explicit attention to GE effects in future evaluations of credit market interventionsis likely warranted.

6In a forebearer to this literature, McCloskey and Nash (1984) attribute the dramatic reduction in seasonal grainprice fluctuations observed in England between the 14th and 17th centuries to a reduction in interest rates.

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Barrett (2011) argue that credit constraints substantially alter smallholder farmers’ marketing and

storage decisions, and Basu and Wong (2012) show that allowing farmers to borrow against future

harvests can substantially increase lean-season consumption. Similarly, Dillion (2017) finds that

an administrative change in the school calendar that moved the timing of school fee payments to

earlier in the year in Malawi forced credit constrained households with school-aged children to sell

their crops earlier and at a lower price. Fink et al. (2014) shows that agricultural loans aimed at

alleviating seasonal labor shortages can improve household welfare in Zambia, while Beaman et al.

(2014) find in Mali that well-timed credit access can increase investment in agricultural inputs.

As in these related papers, our results show that financial market imperfections lead households

to turn to increasingly costly ways to move consumption around in time. In our particular setting,

credit constraints combined with post-harvest cash needs cause farmers to store less than they

would in an unconstrained world. In this setting, even a relatively modest expansion of credit

affects local market prices, to the apparent benefit of both those with and without access to this

credit.

The remainder of the paper proceeds as follows. Section 2 describes the setting and the ex-

periment. Section 3 describes our data, estimation strategy, and pre-analysis plan. Section 4

presents baseline estimates ignoring the role of general equilibrium effects. Section 5 presents the

market level effects of the intervention. Section 6 shows how these market-level effects shape the

individual-level returns to the loan. Section 7 concludes.

2 Setting and experimental design

2.1 Arbitrage opportunities in rural grain markets

Seasonal fluctuations in prices for staple grains appear to offer substantial intertemporal arbitrage

opportunities, both in our study region of East Africa as well as in other parts of the developing

world. While long-term price data do not exist for the small, rural markets where our experiment

takes place, price series data are available for major markets throughout the region. Average

seasonal price fluctuations for maize in available markets are shown in Figure 1. Increases in maize

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prices in the six to eight months following harvest average roughly 25-40% in these markets; price

increase reported elsewhere in Africa are consistent with these figures, if not higher.7

These increases also appear to be a lower bound on typical increase observed in the smaller

markets in our study area, which (relative to these much larger markets) are characterized with

much smaller “catchments” and less outside trade. We asked farmers at baseline to estimate average

monthly prices of maize at their local market point over the five years prior to our experiment. As

shown in Panel A of Figure 4, they reported a typical doubling in price between September (the

main harvest month) and the following June.8 We also collected monthly price data from local

market points in our sample area during the two years of this study’s intervention, as well as for a

year after the intervention ended (more on this data collection below).9 Panel B of Figure 4 presents

the price fluctuations observed during this period. Because data collection began in November 2012

(two months after the typical trough in September), we cannot calculate the full price fluctuation

for the 2012-2013 season. However, in the 2013-2014 and 2014-2015 seasons we observe prices

increasing by 42% and 45% respectively. These are smaller fluctuations than those seen in prior

years (as reported by farmers in our sample) and smaller than those seen in subsequent years, which

saw increases of 53% and 125% respectively.10 There is therefore some variability in the precise

size of the price fluctuation from season to season. Nevertheless, we see price consistently rise by

more than 40% and, in some years, by substantially more.

These fluctuations have meaningful and negative consequences for the welfare of rural house-

holds. Food price seasonality drives large fluctuations in consumption, with both food and non-food

consumption dropping noticeably during the lean season (Kaminski and Gilbert, 2014; Basu and

7For instance, Barrett (2007) reports seasonal rice price variation in Madagascar of 80%, World Bank (2006)reports seasonal maize price variation of about 70% in rural Malawi, and Aker (2012) reports seasonal variation inmillet prices in Niger of 40%.

8In case farmers were somehow mistaken or overoptimistic, we asked the same question of the local maize tradersthat can typically be found in these market points. These traders report very similar average price increases: theaverage reported increase between October and June across traders was 87%. Results available on request.

9The study period covers the 2012-2013 and 2013-2014 season. We also collect data for one year after the studyperiod, covering the 2014-2015 season, in order to align with the long-run follow-up data collection on the farmerside.

10For the 2015-2016 season, we combine our data with that collected by Bergquist (2017) in the same county inKenya and estimate that maize prices increased by 53% from November to June. For the 2016-2017 season, we thankPascaline Dupas for her generosity in sharing maize price data collected in the same county in November 2016 andJune 2017, from which we estimate an increase of 125%.

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Wong, 2012). Barrett and Dorosh (1996) find that the greatest burden of such price fluctuations

falls on the poorest of farmers.

These price fluctuations are surprising in light of the storable nature of staple commodities.

Home storage is a simple technology available to farmers in this region. To store, farmers dry

maize kernels on a tarp immediately after harvest, treat the crop with insecticide dust, and store

it in locally-made sacks, kept on wooden pallets to allow for air circulation and typically located

in farmers’ homes or in small outdoor sheds. Our survey data suggests the cost of these storage

materials is low, at around 3.5% of the value of the crop at harvest time. Post-harvest losses

also appear minimal in this setting, with an average of 2.5% of the crop lost over a 6-9 month

storage period (see Appendix B for further discussion). The low cost of storage, in conjunction

with consistently large price increases over the course of the season, therefore appears to offer large

opportunities for arbitrage.

However, farmers do not appear to be taking advantage of these apparent arbitrage opportuni-

ties. Figure A.1 shows data from two earlier pilot studies conducted either by our NGO partner (in

2010/11, with 225 farmers) or in conjunction with our partner (in 2011/12, with a different sample

of 700 farmers). These studies tracked maize inventories, purchases, and sales for farmers in our

study region. In both years, the median farmer exhausted her inventories about 5 months after

harvest, and at that point switched from being a net seller of maize to a net purchaser as shown in

the right panels of the figure. This was despite the fact that farmer-reported sales prices rose by

more than 80% in both of these years in the nine months following harvest.

Why are farmers not using storage to sell grain at higher prices and purchase at lower prices?

Our experiment is designed to test one specific explanation: that credit constraints limit farmers

ability to arbitrage these price fluctuations.11 In extensive focus groups with farmers prior to

our experiment, credit constraints were the unprompted explanation given by the vast majority

of these farmers as to why they sold the majority of their maize in the immediate post-harvest

period. In particular, because nearly all of these farm households have school-aged kids, and

a large percentage of a child’s school fees are typically due in the few months after harvest in

11Other factors, mostly outside the scope of this paper, may also be at play in limiting farmers’ ability to store.Appendix B explores these other factors in greater detail.

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January, given the calendar-year school year schedule, many farmers report selling much of their

harvest to pay these fees. Indeed, many schools in the area will accept in-kind payment in maize

during this period. Farmers also report having to pay other bills they have accumulated throughout

the year during the post-harvest period. Finally, many farmers also spend more on discretionary

expenditures during this harvest period as well, which may be reflective of high levels of impatience

or present-biased preferences. Regardless of the source, harvest is a time of large expenditure.

Why do these high harvest-time expenditures necessitate high harvest-time sales of maize? In

the absence of functioning financial markets, the timing of production and consumption – or, more

specifically, sale and expenditure – must be intimately tied. As with poor households throughout

much of the world, farmers in our study area appear to have very limited access to formal credit.

Only eight percent of households in our sample reported having taking a loan from a bank in the

year prior to the baseline survey.12 Informal credit markets also appear relatively thin, with fewer

than 25% of farmers reporting having given or received a loan from a moneylender, family member,

or friend in the 3 months before the baseline.

Absent other means of borrowing, and given the high expenditure needs they report facing

in the post-harvest period, farmers end up liquidating grain rather than storing. Furthermore, a

significant percentage of these households end up buying back maize from the market later in the

season to meet consumption needs, and this pattern of “sell low and buy high” directly suggests

a liquidity story: farmers are in effect taking a high-interest quasi-loan from the maize market

(Stephens and Barrett, 2011). Baseline data indicate that 35% of our sample both bought and

sold maize during the previous crop year (September 2011 to August 2012), and that over half

of these sales occurred before January (when prices were low). 40% of our sample reported only

purchasing maize over this period, and the median farmer in this group made all of their purchases

after January. Stephens and Barrett (2011) report similar patterns for other households in Western

Kenya during an earlier period.

12Note that even at the high interest rates charged by formal banking institutions (typically around 20% annually),storage would remain profitable, given the 40% plus (often much larger) increases in prices that are regularly observedover the 9-month post-harvest period and relatively small storage costs and losses (e.g., due to spoilage), which weestimate to be less than 6%.

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2.2 Experimental design

To test the hypothesis that the limited availability of credit constrains farmers from taking ad-

vantage of the arbitrage opportunities presented by seasonal price fluctuations, we partner with

the organization One Acre Fund (OAF) to offer farmers harvest-time loan. OAF is a microfinance

NGO that makes in-kind, joint-liability loans of fertilizer and seed to groups of farmers, as well

as providing training on improved farming techniques. OAF group sizes typically range from 8-12

farmers, and farmer groups are organized into “sublocations” – effectively clusters of villages that

can be served by one OAF field officer.13 OAF typically serves about 30% of farmers in a given

sublocation.

The study sample is drawn from existing groups of One Acre Fund (OAF) farmers in Webuye

and Matete districts in Western Kenya. The Year 1 sample consists of 240 existing OAF farmer

groups drawn from 17 different sublocations in Webuye district, and our total sample size at baseline

was 1,589 farmers. The Year 2 sample attempts to follow the same OAF groups as Year 1; however,

some groups dissolved such that in Year 2 we are left with 171 groups. In addition, some of the

groups experienced substantial shifting of the individual members; therefore some Year 1 farmers

drop out of our Year 2 sample, and other farmers are new to our Year 2 sample.14 Ultimately, of

the 1,019 individuals in our Year 2 sample, 602 are drawn from the Year 1 sample and 417 are new

to the sample.

Figure 4 displays the experimental design. There are two main levels of randomization. First,

we randomly divided the 17 sublocations in our sample into 9 “high” intensity” sites and 8 “low

intensity” sites. In high intensity sites, we enrolled 80% of OAF groups in the sample (for a

sample of 171 groups), while in low intensity sites, we only enrolled 40% of OAF groups in the

sample (for a sample of 69 groups). Then, within each sublocation, groups were randomized into

treatment or control. In Year 1, two-thirds of individuals in each sublocation were randomized into

13A sublocation is a group of 4-5 villages, with a typical population of 400-500 people.14Shifting of group members is a function of several factors, including whether farmers wished to participate in the

overall OAF program from year to year. There was some (small) selective attrition based on treatment status in Year1; treated individuals were 10 percentage points more likely to return to the Year 2 sample than control individuals(significant at 1%). This does slightly alter the composition of the Year 2 sample (see Table L.3 and Section L), butbecause Year 2 treatment status is stratified by Year 1 treatment status (as will be described below), it does not alterthe internal validity of the Year 2 results.

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treatment (more on this below) and one-third into control. In Year 2, half of individuals in each

sublocation were randomized into treatment and half into control. As a result of this randomization

procedure, high intensity sublocations have double the number of treated individuals as in low

intensity sublocations.

The group-level randomization was stratified at the sublocation level (and in Year 1, for which

we had administrative data, further stratified based on whether group-average OAF loan size in

the previous year was above or below the sample median). In Year 2, we maintained the same

saturation treatment status at the sublocation level,15 but re-randomized groups into treatment

and control, stratifying on their treatment status from Year 1.16 Given the roughly 35% reduction

in overall sample size in Year 2, overall treatment saturation rates (the number of treated farmers

per sublocation) were effectively 35% lower in Year 2 as compared to Year 1.

In Year 1, there was a third level of randomization pertaining to the timing of the loan offer.

In focus groups run prior to the experiment, farmers were split on when credit access would be

most useful, with some preferring cash immediately at harvest, and others preferring it a few

months later timed to coincide with when school fees were due (the latter preferences suggesting

that farmers may be sophisticated about potential difficulties in holding on to cash between the

time it was disbursed and the time it needed to be spent). In order to test the importance of loan

timing, in Year 1, a random half of the treated group (so a third of the total sample) received the

loan in October (immediately following harvest), while the other half received the loan in January

(immediately before school fees are due, although still several months before the local lean season).

As will be described in Section 4, results from Year 1 suggested that the earlier loan was more

effective, and therefore in Year 2 OAF only offered the earlier timed loan to the full sample (though

due to administrative delays, the actual loan was disbursed in November in Year 2).

Although all farmers in each loan treatment group were offered the loan, we follow only a

randomly selected 6 farmers in each loan group, and a randomly selected 8 farmers in each of the

15Such that, for example, if a sublocation was a high intensity sublocation in Year 1 it remained a high intensitysublocation in Year 2.

16This was intended to result in randomized duration of treatment – either zero years of the loan, one year of theloan, or two years – however, because the decision to return to the Year 2 sample was affected by Year 1 treatmentstatus, we do not use this variation here and instead focus throughout on one year impacts.

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control groups.

Loan offers were announced in September in both years. The size of the loan for which farmers

were eligible was a linear function of the number of bags they had in storage at the time of loan

disbursal.17 In Year 1, there was a cap of 7 bags for which farmers could be eligible; in Year 2, this

cap was 5 bags. In Year 1, to account for the expected price increase, October bags were valued

at 1500 Ksh, and January bags at 2000 Ksh. In Year 2, bags were valued at 2500 Ksh. Each loan

carried with it a “flat” interest rate of 10%, with full repayment due after nine months.1819 These

loans were an add-on to the existing in-kind loans that OAF clients received, and OAF allows

flexible repayment of both – farmers are not required to repay anything immediately.

OAF did not take physical or legal position of the bags, which remained in farmers’ home stores.

Bags were tagged with a simple laminated tag and zip tie. When we mentioned in focus groups

the possibility of OAF running a harvest loan program, and described the details about the bag

tagging, many farmers (unprompted) said that the tags alone would prove useful in shielding their

maize from network pressure: “branding” the maize as committed to OAF, a well-known lender in

the region, would allow them to credibly claim that it could not be given out.20 Because tags could

represent a meaningful treatment in their own right, we wished to separate the effect of the credit

from any effect of the tag, and therefore in the Year 1 study offered a separate treatment arm in

which groups received only the tags.21

Finally, because self- or other-control problems might make it particularly difficult to channel

cash toward productive investments in settings where there is a substantial time lag between when

the cash is delivered and when the desired investment is made, in Year 1, we also cross-randomized

17However, there was no further requirement that farmers store beyond the date of loan disbursal. This requirementwas set by OAF to ensure that farmers took a “reasonable” loan size that they would be able to repay.

18Annualized, this interest rate is slightly lower than the 16-18% APR charged on loans at Equity Bank, the mainrural lender in Kenya.

19For example, a farmer who committed 5 bags when offered the October loan in Year 1 would receive 5*1500 =7500 Ksh in cash in October (∼$90 at current exchange rates), and would be required to repay 8250 Ksh by the endof July.

20Such behavior is consistent with evidence from elsewhere in Africa that individuals take out loans or use com-mitment savings accounts mainly as a way to demonstrate that they have little to share with others(Baland et al.,2011; Brune et al., 2011).

21This is not the full factorial research design – there could be an interaction between the tag and the loan – butwe did not have access to a sufficiently large sample size to implement the full 2 x 2 design to isolate any interactioneffect.

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a simple savings technology that had shown promise in a nearby setting (Dupas and Robinson,

2013). In particular, a subset of farmers in each loan treatment group in Year 1 were offered a

savings lockbox (a simple metal box with a sturdy lock) which they could use as they pleased.

While such a savings device could have other effects on household decision making, our hypothesis

was that it would be particularly helpful for loan clients who received cash before it was needed.

The tags and lockbox treatments were randomized at the individual level during Year 1. These

treatments were not included in Year 2 due to minimal treatment effects in Year 1 data (discussed

below), as well as the somewhat smaller sample size in Year 2. Using the sample of individuals

randomly selected to be followed in each group, we stratified individual level treatments by group

treatment assignment and by gender. So, for instance, of all of the women who were offered the

October loan and who were randomly selected to be surveyed, one third of them were randomly

offered the lockbox (and similarly for the men and for the January loan). In the control groups, in

which we were following 8 farmers, 25% of the men and 25% of the women were randomly offered

the lockbox, with another 25% each being randomly offered the tags. The study design allows

identification of the individual and combined effects of the different treatments, and our approach

for estimating these effects is described below.

3 Data and estimation

The timing of the study activities is shown in Figure 3. In August/September 2012 (prior to the Year

1 experiment), a baseline survey was conducted with the entire Year 1 sample. The baseline survey

collected data on farming practices, storage costs, maize storage and marketing over the previous

crop year, price expectations for the coming year, food and non-food consumption expenditure,

household borrowing, lending, and saving behavior, household transfers with other family members

and neighbors, sources of non-farm income, time and risk preferences, and digit span recall. Table

N.1 presents summary statistics for a range of variables at baseline; we observe balance on most

of these variables across treatment groups, as would be expected from randomization. Table K.1

shows the analogous table comparing individuals in the high- and low-treatment-density areas; the

samples appear balanced on observables here as well.

13

We then undertook three follow-up rounds over the ensuing 12 months, spanning the spring

2013 “long rains” planting (the primary growing season) and concluding just prior to the 2013 long

rains harvest (which occurs August-September). The multiple follow-up rounds were motivated by

three factors. First, a simple inter-temporal model of storage and consumption decisions suggests

that while the loan should increase total consumption across all periods, the per-period effects could

be ambiguous – meaning that consumption throughout the follow-up period needs to be measured

to get at overall effects. Second, because nearly all farmers deplete their inventories before the

next harvest, inventories measured at a single follow-up one year after treatment would likely

provide very little information on how the loan affected storage and marketing behavior. Finally,

as shown in McKenzie (2012), multiple follow-up measurements on noisy outcomes variables (e.g

consumption) has the added advantage of increasing power. The follow-up surveys tracked data on

storage inventory, maize marketing behavior, consumption, and other credit and savings behavior.

Follow-up surveys also collected information on time preferences and on self-reported happiness.

Because the Year 2 experiment was designed to follow the sample sample as Year 1, a second

baseline was not run prior to Year 2.22 A similar schedule of three follow-up rounds over 12 months

was conducted in Year 2 following the loan disbursal.

Attrition was relatively low across survey rounds. In Year 1, overall attrition was 8%, and not

significantly different across treatment groups (8% in the treatment group and 7% in the control).

In Year 2, overall attrition was 2% (in both treatment and control, with no significant difference).

Year 1 treatment status is predictive of Year 2 re-enrollment in the study (treated individuals

were more likely to re-register for OAF in the second year, perhaps reflecting a positive appraisal of

the value of the loan). However, because Year 2 treatment status was re-randomized and stratified

by Year 1 treatment status, this does not alter the internal validity of the Year 2 results.23, 24

22In practice, due to the administrative shifts in farmer group composition described in greater detail in Section2, 417 of the 1,019 individuals in the Year 2 sample were new to the study. For these individuals, we do not havebaseline data (there was insufficient time between receiving the updated administrative records for Year 2 groups andthe disbursal of the loan to allow for a second baseline to be run). Therefore, balance tables can only be run with thesample that was present in Year 1. Because the loan offer was randomized, however, this should not affect inferenceregarding the impacts of the loan.

23This does, however, mean that we cannot exploit the re-randomization in Year 2 to identify the effect of receivingthe loan for multiple years or of receiving the loan and then having it discontinued, as an endogenously selected groupdid not return to the Year 2 sample and therefore was never assigned a Year 2 treatment status.

24This also slightly alters the composition of the Year 2 sample, relevant to external validity. Appendix L explores

14

In order to explore the long-run effects of the loan, we also ran a Long-Run Follow-Up (LRFU)

survey from November-December 2015. This was two (one) years following loan repayment for

the Year 1 (Year 2) treatment group. This survey followed up on the entire Year 2 sample (1,091

individuals) and a representative subset of the Year 1 only sample (another 481 individuals), for

a total sample of 1500 individuals. The survey collected information on maize harvests, sales,

purchases, and revenues by season from 2014-2015. It also collected data on farm inputs (labor

and capital), food consumption and expenditure, household consumption, educational expenditure

and attendance among children, non-farm employment and revenues, and a self-reported happiness

measure. Attrition in the LRFU was 9%, with no differential attrition based on Year 2 treatment

status and slight differential attrition based on Year 1 treatment status.25 Appendix L provides

further discussion.

In addition to farmer-level surveys, we also collected monthly price surveys at 52 market points

in the study area. The markets were identified prior to treatment based on information from

local OAF staff about the market points in which client farmers typically buy and sell maize.

Data collection for these surveys began in November 2012 and continued through December 2015.

Finally, we utilize administrative data on loan repayment that was generously shared by OAF.

3.1 Pre-analysis plan

To limit both risks and perceptions of data mining and specification search (Casey et al., 2012), we

registered a pre-analysis plan (PAP) for Year 1 prior to the analysis of any follow-up data.26 The

Year 2 analysis follows a near identical analysis plan. The PAP can be found in Appendix N.

We deviate significantly from the PAP in one instance: the PAP specifies that we will analyze

the effect of treatment saturation on the percent price spread from November to June. However,

because in practice the loan was offered at slight different points in time (October and January in

this further.25Being treated in Year 1 is associated with a 3 percentage point increase in the likelihood of being found in the

long-run follow up survey, significant at 10%. This appears to be at least partially driven by the fact that Year 1treated individuals were more likely to be in the Year 2 sample (and therefore had been more recently in touch withour survey team). After controlling for whether an individual was present in the Year 2 sample, Year 1 treatmentstatus is no longer significantly correlated with attrition.

26The pre-analysis plan is registered here: https://www.socialscienceregistry.org/trials/67, and was registered onSeptember 6th 2013. The complete set of results are available upon request.

15

Year 1; November in Year 2) and because there is year-to-year variation in when markets hit their

peak and trough, this measure may fail to capture the full effect of treatment on prices. Moreover,

this measure is statistically underpowered, ignoring 77% of our monthly data by focusing solely on

the price gap between two months, rather than exploiting the full nine months of data collected

over the season.

Therefore, in our primary specifications, we relax our attachment to this underpowered and

perhaps misspecified measure November-June price gap, instead analyze the non-parametric effect

of treatment on the evolution of monthly prices, as well as a level and time trend effect. Appendix

I.3 presents the pre-specified November-June effect. For all analyses, we maintain our original

hypothesis that effect of high-density treatment on prices will be initially positive if receipt of the

loan allows farmers to pull grain off the market in the post-harvest surplus period and later negative

as stored grain is released onto the market.

In two other instances we add to the PAP. First, in addition to the regression results specified

in the PAP, we also present graphical results for many of the outcomes. These results are based

on non-parametric estimates of the parametric regressions specified in the PAP, and are included

because they clearly summarize how treatment effects evolve over time, but since they were not

explicitly specified in the PAP we mention them here. Second, we failed to include in the PAP the

(ex post obvious) regressions in which the individual-level treatment effect is allowed to vary by

the sublocation-level treatment intensity, and present these below.

3.2 Estimation of treatment effects

In all analyses, we present results separately by year and pooled across years. Because the Year

2 replication produced results that are quantitatively quite similar to the Year 1 results for most

outcomes, we rely on the pooled results as our specification of primary interest. However, for the

sake of transparency and comparison, we report both.

There are three main outcomes of interest: inventories, maize net revenues, and consumption.

Inventories are the number of 90kg bags of maize the household had in their maize store at the

time of the each survey. This amount is visually verified by our enumeration team, and so is likely

16

to be measured with minimal error. We define maize net revenues as the value of all maize sales

minus the value of all maize purchases, and minus any additional interest payments made on the

loan for individuals in the treatment group. We call this “net revenues” rather than “profits” since

we likely do not observe all costs; nevertheless, costs are likely to be very similar across treatment

groups (fixed costs of storing at home were already paid, and variable costs of storage are very low).

The values of sales and purchases were based on recall data over the period between each survey

round. Finally, we define consumption as the log of total household expenditure over the 30 days

prior to each survey. For each of these variables we trim the top and bottom 0.5% of observations,

as specified in the pre-analysis plan.

Letting Tjy be an an indicator for whether group j was assigned to treatment in year y, and

Yijry as the outcome of interest for individual i in group j in round r ∈ (1, 2, 3) in year y. The

main specification pools data across follow-up rounds 1-3 (and for the pooled specification, across

years):

Yijry = α+ βTjy + ηry + dt + εijry (1)

The coefficient β estimates the Intent-to-Treat and, with round-year fixed effects ηry, is identified

from within-round variation between treatment and control groups. β can be interpreted as the

average effect of being offered the loan product across follow-up rounds, though as we detail below,

loan take-up was high. To absorb additional variation in the outcomes of interest, we also control

for survey date (dt) in the regressions. Each follow-up round spanned over three months, meaning

that there could be (for instance) substantial within-round drawdown of inventories. Inclusion of

this covariate should help to make our estimates more precise without biasing point estimates.

Standard errors are clustered at the loan group level.

The assumption in Equation 8 is that treatment effects are constant across rounds. In our

setting, there are reasons why this might not be the case. In particular, if treatment encourages

storage, one might expect maize revenues to be lower for the treated group immediately following

harvest, as they hold off selling, and greater later on during the lean season, when they release

their stored grain. To explore whether treatment effects are constant across rounds, we estimate:

17

Yijry =3∑

r=1

βrTjy + ηry + dt + εijry (2)

and test whether the βr are the same across rounds (as estimated by interacting the treatment

indictor with round dummies). Unless otherwise indicated, we estimate both (8) and (9) for each

of the hypotheses below.

To explore heterogeneity in treatment effects, we estimate:

Yijry = α+ β1Tjy + β2Zi0 + β2Tjy ∗ Zi0 + ηry + dt + εijry (3)

where Zi0 is the standardized variable by which we explore heterogeneity, as measured at baseline.

As pre-specified, we explore heterogeneity by impatience (as measured in standard time preference

questions), the number of school-aged children, the initial liquid wealth level, the percent of baseline

sales sold early (prior to January 1), and the seasonal price increase expected between September

2012 and June 2013. Because a baseline was only run prior to Year 1, we are only able to present

these specifications for the Year 1 intervention.

To quantify market level effects of the loan intervention, we tracked market prices at 52 market

points throughout our study region, and we assign these markets to the nearest sublocation. To

estimate price effects we begin by estimating the following linear model:

pmsty = α+ β1Hs + β2montht + β3(Hs ∗montht) + εmst (4)

where pmst represents the maize sales price at market m in sublocation s in month t in year

y.27 Hs is a binary variable indicating whether sublocation s is a high-intensity sublocation, and

montht is a time trend (in each year, Nov = 0, Dec = 1, etc). If access to the storage loan allowed

farmers to shift purchases to earlier in the season or sales to later in the season, and if this shift in

marketing behavior was enough to alter supply and demand in local markets, then our prediction is

that β1 > 0 and β3 < 0, i.e. that prices in areas with more treated farmers are higher after harvest

27Prices are normalized to 100 among the “low” intensity markets in the first month (Hs = 0, montht = 0).Therefore, price effects can be interpreted as a percentage change from control market post-harvest prices.

18

but lower closer to the lean season.

While Hs is randomly assigned, and thus the number of treated farmers in each sublocation

should be orthogonal to other location-specific characteristics that might also affect prices (e.g. the

size of each market’s catchment), we have only 17 sublocations. This relatively small number of

clusters could present problems for inference (Cameron et al., 2008). We begin by clustering errors

at the sublocation level when estimating Equation 4. We also report standard errors estimated

using both the wild bootstrap technique described in Cameron et al. (2008) and the randomization

inference technique used in Cohen and Dupas (2010).

To understand how treatment density affects individual-level treatment effects, we estimate

Equations 8 and 9, interacting the individual-level treatment indicator with the treatment density

dummy. The pooled equation is thus:

Yijsry = α+ β1Tjy + β2Hs + β3(Tjy ∗Hs) + ηry + dt + εijsry (5)

If the intervention produces sufficient individual level behavior to generate market-level effects, we

predict that β3 < 0 and perhaps that β2 > 0 - i.e. treated individual in high-density areas do worse

than in low density areas, and control individuals in high density areas do better than control

individuals in low density areas. As in Equation 4, we report results with errors clustered at the

sublocation level.

For long-run effects, we first estimate the following regression for each year separately:

Yij = α+ βTjy + εij (6)

in which Yij is the outcome of interest for individual i in group j. The sample is restricted to those

who were in the Year y study.

We further also estimate the following specification:

Yij = α+ β1Tj1 + β2Tj2 + β3Tj1 ∗ Tj2 + εij (7)

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in which Tj1 is an indicator for being an in treated group in year 1, Tj12 is an indicator for being

in a treated group in year 2, and Tj1 ∗ Tj2 is an interaction term for being in a group that was

treated in both years. The sample is restricted to those who were in the study for both years.

Because of this sample restriction, and because decision to return to the sample from the Year 1

to Year 2 study was differential based on treatment status (see Appendix L), this last specification

is open to endogeneity concerns and therefore should not be interpreted causally. For the sake of

transparency, we present it regardless, but with the aforementioned caveat.

4 Individual level results

4.1 Harvest loan take up

Take-up of the loan treatments was quite high. Of the 954 individuals in the Year 1 treatment

group, 610 (64%) applied and qualified for the loan. In Year 2, 324 out of the 522 treated individuals

(62%) qualified for and took up the loan.28

Unconditional loan sizes in the two treatment groups were 4,817 Ksh and 6,679 Ksh, or about

$57 and $79 USD, respectively. The average loan sizes conditional on take-up were 7,533 Ksh (or

about $89 USD) for Year 1 and 10,548 Ksh (or $124) for Year 2.29. Default rates were extremely

low, at less than 2%.

28Relative to many other credit-market interventions in low-income settings in which documented take-up ratesrange from 2-55% of the surveyed population (Karlan et al., 2010), the 60-65% take-up rates of our loan productwere very high. This is perhaps not surprising given that our loan product was offered as a top-up for individualswho were already clients of an MFI. Nevertheless, OAF estimates that about 30% of farmers in a given village inour study area enroll in OAF, which implies that even if no non-OAF farmers were to adopt the loan if offered it,population-wide take-up rates of our loan product would still exceed 15%.

29Recall in Year 1 there were two versions of the loan, one offered in October and the other in January. Of the 474individuals in the 77 groups assigned to the October loan treatment (T1), 329 (69%) applied and qualified for theloan. For the January loan treatment (T2), 281 out of the 480 (59%) qualified for and took up the loan. Unconditionalloan sizes in the two treatment groups were 5,294 Ksh and 4,345 Ksh (or about $62 and $51 USD) for T1 and T2,respectively, and we can reject at 99% confidence that the loan sizes were the same between groups. The averageloan sizes conditional on take-up were 7,627Ksh (or about $90 USD) for T1 and 7,423Ksh (or $87) for T2, and inthis case we cannot reject that conditional loan sizes were the same between groups.

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4.2 Primary effects of the loan offer

We begin by estimating treatment effects in the standard fashion, assuming that there could be

within-randomization-unit spillovers (in our case, the group), but that there are no cross-group

spillovers. In all tables and figures, we report results broken down by each year and pooled. As

explained in Section 3, the Year 2 replication produced results that are quantitatively quite similar

to the Year 1 results for most outcomes, and as such, we report in the text the pooled results,

unless otherwise noted.

Tables 2-4 and Figure 5 present the results of estimating Equations 8 and 9 on the pooled

treatment indicator, either parametrically (in the table) or non-parametrically (in the figure). The

top panels in Figure 5 show the means in the treatment group (broken down by year and then

pooled, in the final panel) over time for our three main outcomes of interest (as estimated with Fan

regressions). The bottom panels present the difference in treatment minus control over time, with

the 95% confidence interval calculated by bootstrapping the Fan regression 1000 times.

Farmers responded to the intervention as anticipated. They held significantly more inventories

for much of the year, on average about 25% more than the control group mean (Column 6 in Table

2). Inventory effects are remarkably similar across both years of the experiment.

Net revenues30 are significantly lower immediately post harvest and significantly higher later

in the year (Column 6 in Table 3). The middle panel of Figure 5 presents the time trend of net

revenue effects, which suggest that treated farmers purchase more maize in the immediate post-

harvest period, when prices are low (as represented by more negative net revenues November to

February) and sell more later in the lean season, when prices are high (as represented by more

positive revenues May to July). The net effect on revenues averaged across the year is positive in

both years of the experiment, and is significant in the Year 2 and the pooled data (see Columns 1,

3, and 5 in Table 3). Breaking down Year 1 results by the timing of loan suggest that the reason

results in Year 1 are not significant is that the later loan, offered in January to half of the treatment

group, was less effective than the October loan. Table D.1 presents results for the Year 1 loan,

broken down by loan timing. We see in Column 5 that the October loan (T1) produced revenue

30From which loan interest rates were subtracted for those who took out a loan.

21

effects that are more similar in magnitude (and now significant, at 5%) to those of the Year 2 loan

(which was offered almost at the same time). The January loan (T2) had no significant effect on

revenues. Appendix Section D explores the effects of loan timing in greater detail.

The total effect on net revenues across the year can be calculated by adding up the coefficients in

Column 6 of Table 3,which yields an estimate of 1,548 Ksh, or about $18 at the prevailing exchange

rate at the time of the study. Given the unconditional average loan size of 5,476 Ksh in the pooled

data, this is equivalent to a 28% return (net of loan and interest repayment), which we consider

large.

The final panel of Figure 5 and Table 4 present the consumption effects (as measured by logged

total household consumption). While point estimates are positive in both years, they are not

significant at traditional confidence levels when pooled (in Year 2, treatment is associated with a 7

percentage point increase in consumption, significant at 10%, but in Year 1, estimated effects are

only slightly greater than zero and are not significant).31

Table 5 presents effects on the pattern of net sales (quantity sold - quantity purchased), as

well as prices paid and received. We see that in the immediate post-harvest period, net sales are

significantly lower among the treated group, as sales decrease/purchases increase. Later in the

season, this trend reverses, as net sales significantly expand among the treated. As a result of this

shifted timing of sales and purchases, treated individuals enjoy significantly lower purchase prices

(as prices are shifted to earlier in the season, when prices tend to be lower) and receive significantly

higher sales prices (as sales are shifted to later in the season, when prices tend to be higher). The

total impact on net sales is a weakly positive effect, which – off of a negative average net sales

amount – means that households are slightly less in deficit.32,33

31Because the consumption measure includes expenditure on maize, in Appendix E.1 we also estimate effects onconsumption excluding maize and consumption excluding all food. Results are similar using these measures.

32Unlike the impact on net sales per round, on which we have strong theoretical predictions, the impact on totalnet sales is ex-ante ambiguous, from a theoretical perspective. In practice, the total effect on net sales will be acombined response of the increase in purchases in response to lower effective purchase prices and increases in salesin response to higher effective sales prices. Valuing the increase in net sales, we estimate that 48% of the increase inrevenues among treated individuals is driven by an increase in net sales and 52% by a shifting in the timing of sales.

33From where is the increase in net sales drawn? We assume net sales = amount harvested - post-harvest losses- amount consumed - amount transferred and decompose the treatment effect on each component part. We see amarginally significant (at 10%) increase in amount that treated households transfer to others by 0.2 bags. We areunable to identify with precision any effects on the other components of net sales (results available upon request).

22

4.3 Heterogeneity

Tables C.1-C.3 in Appendix C present the pre-specified dimensions of heterogeneity in treatment

effects on inventories, revenues and log household consumption. Because the pre-specified specifica-

tion is an intention-to-treat estimation, we also present a regression of take-up on the standardized

variable of heterogeneity. While we see greater take-up of the loan by impatient households and

households with more school-aged children, we see no significant heterogeneity in treatment ef-

fects by these dimensions. We observe slightly larger treatment effects among wealthy households

(marginally significant for revenue outcomes, but not significant for inventories or consumption).

Interestingly, we see significantly and large increases in the estimated treatment effects for house-

holds with a larger percentage of early sales at baseline (that is, those who were less likely to store

at baseline). It may be that these households have the greatest room for movement in storage

behavior and/or that these households were most constrained at baseline. For inventories and

revenues, treatment appears to cut in half the gap between the baseline storers and non-storers.

Expectations regarding the impending seasonal price increase does not appear to be related to

take-up or treatment effects.

4.4 Secondary effects of the loan offer

Appendix Section E presents outcomes on potential secondary outcomes of interest. We find no

significant effects on profits earned from and hours worked at non-farm household-run businesses

(Tables E.1-E.2), nor on wages earned from and hours worked in salaried employment (Tables E.3

and E.4). We also find no significant effects on schools fees paid (the primary expenditure that

households say constrain them to sell their maize stocks early; see Table E.7), nor do we find

significant effects on food expenditure (Table E.5). We do in Year 1 find a significant 0.07 point

increase on a happiness index (an index for the following question: “Taking everything together,

would you say you are very happy (3), somewhat happy (2), or not happy (1)”). However, we find

no significant increase in this measure in Year 2.

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4.5 Long-run effects

Appendix Section F presents the long-run effects of the loan, as measured in the Long-Run Follow-

Up (LRFU) survey conducted November-December 2015, which measures outcomes one to two

years after completion of the intervention (for the Year 2 and Year 1 loan respectively). In this

section, we primarily focus on the effects of each year of the study as estimated separately, as these

results can be interpreted causally. For the sake of transparency, we also present a specification

with the two treatment years interacted, but with the aforementioned caveats described in Section

3.

We first explore outcomes for the 2014 long-rains harvest, the season immediately following

the completion of the Year 2 study. If farmers are able to use revenues from the one- (sometimes

two-) time loan to “save their way” out of this credit constraint, we should expect to see sustained

shifts in the timing of sales, as well as long-run revenue effects. However, in Table F.1 we observe

no statistically significant differences in the timing of transactions (neither in terms of the percent

of purchases conducted in the low-price harvest season nor the percent of sales conducted in the

high-price lean season). We also see no statistically significant difference in long-run net revenues

(though due to the imprecision of these estimates, we cannot rule out large, positive effects).34 We

also see no long-run effect on amount and value sold or purchased (Tables F.2-F.4), though again

estimates are relatively noisy.

We are able to ask more detailed questions about the subsequent season (the 2015 long-rains

harvest), which occurred immediately prior to the LRFU survey and therefore required shorter

recall. Measuring impacts on input usage and harvest levels, we test the hypothesis that loan

34While we see no significant changes in sales timing or revenue in among the pooled treatment group, we see whenbreaking these results down by treatment status some interesting heterogeneity (see Table F.10. Point estimatessuggest (and are significant in Year 2) that the percent sold in the lean season and the percent purchased in theharvest season are higher in low-saturation areas. In high saturation areas, the negative interaction terms cancelsthis effect out (see Table F.10). This is consistent with the idea that in low intensity areas, the lack of effect onprices means storage is highly profitable, encouraging individuals to purchase more in the post-harvest period andsell more in the lean season. In contrast, in high intensity areas, price effects dampen the returns to arbitrage, andthere is lower incentive to store. However, we see that control individuals in high intensity areas may be storingmore, buying more (significant among Year 2 individuals) in the harvest period, when prices are low. As a result, wesee cannot rule out sizable increases in revenues for control individuals in high-intensity areas; though this effect ismeasured with considerable noise, it is consistent with the idea that control individuals may benefit from the loan.See Appendix F for greater discussion of this heterogeneity.

24

access produced long-run increases in on-farm investment.35 However, Table F.5 suggests little

movement on this margin. We estimate fairly precise null effects on labor inputs, non-labor inputs,

and 2015 long-rains harvest levels.

We also explore other outcomes for the 2015 year. We find no significant effects on a variety

of outcomes, including: maize eaten, food expenditures, consumption, educational expenditure,

school attendance, non-farm enterprise profits, hours worked in non-farm enterprises, and hours

worked in salaried positions (Tables F.6 - F.8). Point estimates on wages in salaried positions are

positive, but is only significant in Year 2. Finally, we see slight increases in self-reported happiness,

but only among the Year 1 treated sample.

In summary, while we cannot rule out potentially large long-run effects on revenues, we find

no significant evidence that the loan permanently alters farmers’ timing of sales or a variety of

other household-level economic outcomes. Consistent with this, we find no long-run effects on local

market prices (though effects are in the same direction as the short-run effects, but are much muted;

see Table F.9). We therefore find little evidence that a one-time injection of credit can permanently

ameliorate the underlying constraints limiting arbitrage.

4.6 Temptation and kin tax

To test whether self-control issues or social pressure to share with others limits storage, we test

the impact of laminated tags that brand the maize as committed to OAF. Estimates are shown in

Table 13. We find no significant difference in inventories, revenues, or consumption for individuals

who receive only the tags (without the loan), and point estimates are small. Therefore, the tags do

not appear to have any effect on storage behavior. However, this may simply be because tags are

a weak form of commitment, either to one’s self or to others.

35This could occur if revenues from the loan relaxed credit constraints that previously restricted farmers’ abilityto invest in inputs. Alternatively, if the loan led to long-run improvements in the price farmers receive for theircrops, this increased output price could increase incentives to invest in production-enhancing inputs. An improvedprice could be attained either in the lean season, if the farmer in question himself stores, or at harvest time, if otherfarmers are arbitraging and producing lower overall season price fluctuations (though note in Tables F.1 and F.9 wesee no evidence of such long-run shifts in either sales timing or prices).

25

4.7 Savings one’s way out of the credit constraint

How long might it take for a farmer to “save his way out” of this credit constraint? In Appendix

H, we present various estimates suggesting that it would take the farmer 3-6 years to self-finance

the loan, if he were to save the full returns from his investment, but 34 years if he saved at a more

standard savings rate of 10%. Therefore, low savings rates are important to understanding why

credit constraints persist in the presence of high return, divisible investment opportunities.

In order to test the importance of savings constraints, we examine the impact of the lockbox,

as well as its interaction with the loan. Table H.1 presents these results. We observe no significant

effects of the lockbox on inventories, revenues, or consumption in the overall sample. Interestingly,

when interacted with the loan, we see that receiving the lockbox alone is associated with significantly

lower inventories; perhaps the lockbox serves as a substitute savings mechanism, rather than grain.

However, receiving both the lockbox and the loan is associated with a reversal of this pattern.

We see no such heterogeneity on revenues. Interestingly, the point estimates on consumption are

negative (though not significant) for the lockbox and loan when received separately; however, the

interaction of the two is positive (and significant, at 95%), canceling out this effect.

5 General equilibrium effects

Because the loan resulted in greater storage, which shifted supply across time, and given the high

transport costs common in the region, we might expect this intervention to affect the trajectory

of local market prices. By shifting sales out of a relative period of abundance, we would expect

the loan to result in higher prices immediately following harvest. Conversely, by shifting sales into

a period of relative scarcity, we would expect the loan to result in lower prices later in the lean

season. Note, however, that these effects will only be discernible if (1) the treatment generates a

substantial shock to the local supply of maize; and (2) local markets are somewhat isolated, such

that local prices are at least partially determined by local supply.

26

5.1 Market level effects

To understand the effect of our loan intervention on local maize prices, we identified 52 local market

points spread throughout our study area where OAF staff indicated their clients typically bought

and sold maize, and our enumerators tracked monthly maize prices at these market points. We

then match these market points to the OAF sublocation in which they fall.

A note on the matching process: “sublocation” is an OAF administrative unit that is well-

defined in terms of client composition (i.e. OAF divides its farmer groups into sublocations based

on geographic proximity), but which is less well-defined in terms of precise geographic boundaries

(that is, no shape file of sublocations exists). Given this, we use GPS data on both the market

location and the location of farmers in our study sample to calculate the “most likely” sublocation,

based on the designated sublocation to which the modal study farmer falling within a 3km radius

belongs.36 This procedure, include the radius to be used, was pre-specified. As was also pre-

specified, we test robustness to alternative radii of 1km and 5km.

We then utilize the sublocation-level randomization in treatment intensity to identify market-

level effects of our intervention, estimating Equation 4 and clustering standard errors at the sublo-

cation level. Regression results are shown in Table 6 and plotted non-parametrically in Figure 6.

In each year, we explore the price changes from the period following loan disbursal (November in

Year 1, December in Year 2) until the beginning of the subsequent harvest (August in both years).

In Figure 6, which presents the pooled data, we see prices in high-intensity markets on average

start out almost 4% higher in the immediate post-harvest months. As the season progresses, prices

in high-density markets begin to converge and then dip below those low-density markets, ending

almost 2% lower in high-density areas compared to low-density. Table 6 presents these results

according to the empirical specifically outlined in Section 3. In line with the graphic results visible

in Figure 6, here we see the interaction term on “Hi” treatment intensity is positive (and significant

at 5%), while the interaction term between the monthly time trend and the high intensity dummy

is negative (though not significant). Columns 4-5 display robustness to alternative radii; we find

36Because we draw twice the sample from high-intensity areas compared to low (in accordance with our randomizedintensity), we weight the low-intensity observations by two to generate a pool reflective of the true underlying OAFpopulation. From this pool, we identify the modal farmer sublocation.

27

similar point estimates.

The overall picture painted by the market price data is consistent with the individual-level

results presented above. Price effects are most pronounced (and statistically significant) early on

in the season. This is when we observe the largest and most concentrated shock to the supply on

the market (note in Table 2 that the greatest shift in inventories is seen in Round 1). Sensibly,

treatment effects are most concentrated around the time of the loan disbursal, which represents a

common shock affecting all those taking out the loan; this produces a simultaneous inward shift in

supply in the post-harvest period. In contrast, the release of this grain onto the market in the lean

period appears to happen with more diffuse timing among those the treatment group (as can be

seen in Figure 5, in which we note a gradual reduction in the treatment-control gap in inventories,

rather than the sharp drop we would expect if all treated individuals sold at the same time).

Anecdotally, farmers report that the timing of sales is often driven by idiosyncratic shocks to the

household’s need for cash, such as the illness of a family member, which may explain the observed

heterogeneity in timing in which the treatment group releases its stores. Perhaps as a result of

these more diffuse treatment effects in the lean season, price effects are smaller and measured with

larger standard errors in the second half of the year.

Are the size of these observed price effects plausible? A back-the-envelope calibration exercise

suggests yes. OAF works with about 30% of farmers in the region. Of these farmers, 80% were

enrolled in the study in high density areas, while 40% were enrolled in low-density areas. About

58% of those enrolled received the loan offer 37 Together, this implies that about 14% of the

population was offered treatment in high-intensity sublocations and 7% in low-intensity areas, such

that the treatment was offered to 7 percentage points more of the population in high-density areas.

Table 2 suggests that treated individuals experienced average increases in inventory (i.e. inward

supply shifts) of 24.5%. Taken together, this suggests a contraction in total quantity available in

the high-density markets by 1.7%. Experiments conducted in the same region in Kenya suggest

an average demand elasticity of -1.1 (Bergquist, 2017). This would imply that we should expect

37In Year 1, 66% of the sample received the loan offer (1/3 received the offer in October, 1/3 received the loan offerin January, and 1/3 served as control). In Year 2, 50% of the sample received the loan offer (1/2 received the offerin November and 1/2 served as control). In this calibration exercise, we use the average of the two years’ rates.

28

to see an overall price increase of 1.5%. In the period immediately following harvest, when the

inventory effects are most concentrated – during which time inventories are 47.7% higher among

treatment individuals – we see an inward supply shift of 3.3%, and should therefore expect to see

a 3.0% increase in price.38 This is quite close to what we observe in Figure 6. We see a jump in

price of about 2.5% during this period,39 which then peters out to a slightly negative (though not

significant) effect towards the end of the season.

5.2 Robustness checks

We check the robustness of the regression results to functional form assumptions. Table I.1 presents

a binary version of Equation 4, replacing montht with an indicator leant for being in the lean

season (defined as April-August) and the interaction term with leant ∗Hs. Results suggest similar

significant increases in price post-harvest in high-intensity markets. The lean season interaction

term suggests that prices in high-intensity markets are lower overall in the lean season, although

the point estimate on the interaction term is only slightly larger in absolute value than the the

main Hs treatment coefficient, such that the combined effect of treatment in the lean season is to

lower prices in high-intensity markets only slightly below those in low-intensity overall. Comparing

these effects to Figure 6, we observe this is because at the beginning of the lean season prices are

still higher in high intensity markets, with a cross-over mid-lean season as prices in high-intensity

markets drop below those low-intensity markets. However, the 1km and 5km specifications shown

in the right panel in Figure 6 shows suggest that this crossover occurs closer to the transition from

the harvest to lean season; therefore the 1km and 5km specification of the binary specification,

shown in Columns 4-5 of Table I.1, estimate a more substantial decrease in price for the full lean

season.

We also check the robustness of these results to a more continuous measure of treatment at

38Note this exercise assumes no trade across sublocations. On the opposite extreme, the case of perfect marketintegration with zero transaction costs would imply perfect smoothing of any localized supply shock, and we wouldtherefore observe no change in price. We therefore view the range of 0-3% as the extreme bounds of what pricechanges we should expect to observe.

39We measure shifts in post-harvest inventories in Round 1 of the survey, which conducted roughly January-February for the average respondent. We therefore estimate the change in price change in January-February fromTable 6 to be 3.97 + 2.5 ∗ (−0.57) = 2.5.

29

the market-level, following the technique described in Miguel and Kremer (2004). We construct

an estimate of the ratio of total treated farmers to the total farmers in our sample within a 3km

radius around each market.40 We re-estimate an equation identical to Equation 4 with Hs re-

placed with ratiom, the aforementioned ratio. Results are presented in Table I.2. We also present

non-parametric estimates of this specification in Figure I.1, displaying average prices in markets

with above- vs. below-median ratios. While results are somewhat less precisely estimated in this

specification, the broad patterns remain consistent: prices are higher in the post-harvest period

and lower in the lean period in markets with a greater proportion of treated individuals in the area.

We also check robustness to small cluster standard error adjustments. These market-level price

results rely on the treatment saturation randomization being conducted at the sublocation level (a

higher level than the group-level randomization employed in the individual-level results). While

we cluster standard errors at the sublocation level,41 one might be concerned due to the small

number of sublocations – of which we have 17 – that asymptotic properties may not apply to our

market-level analyses and that our standard errors may therefore be understated. We run several

robustness checks to address these small sample concerns. In Appendix I, we use a nonparametric

randomization inference approach employed by Bloom et al. (2013) and Cohen and Dupas (2010) to

draw causal inferences in the presence of small samples. Results using these alternative approaches

are broadly consistent with those from the primary specifications. We also check the robustness of

our results by conducting the wild bootstrap procedure proposed by Cameron et al. (2008). While

we do see some decrease in statistical precision, these adjustments are small. Finally, to ensure

that results are not sensitive to a single outlier sublocation, we drop each sublocation one-by-one

and re-run our analysis; the pattern observed in the full data is generally robust to this outlier

analysis. See Appendix I for further details.

40Because we draw twice the sample from high-intensity areas compared to low (in accordance with our randomizedintensity), for the total farmer count, we weight the low-intensity observations by two to generate a count reflectiveof the true underlying OAF population.

41For all analyses in this paper, we cluster our standard errors at the level of randomization. For the individualresults shown in Section 4, this is at the group level. For the results presented in this section, which relying on thesublocation-level randomized saturation, we cluster at the sublocation level.

30

5.3 Related Outcomes

We also check whether treatment intensity affected other outcomes of interest related to market

price. First, we check whether treatment effects can be seen in farmgate prices (see Table I.5). We

see similar patterns in these prices as well. We also explore whether trader movement responds

to treatment. We see some evidence that fewer traders enter high-intensity treated markets in the

immediate post-harvest period in Year 2 (see Table I.6), a sensible demand response to the increase

in price observed during a time when traders are typically purchasing.42

6 Individual results with spillovers

Mass storage appears to raise prices at harvest time and lower price in the lean season, thereby

smoothing out seasonal price fluctuations. What effect does this have on the individual profitability

of the loan, which is designed to help farmers to take advantage of these price variations? That is,

how do the individual-level returns to arbitrage vary with the number of arbitrageurs?43

To answer this question, we revisit the individual results, re-estimating them to account for

the variation in treatment density across sublocations. Table 7 and Figure 7 display how our main

outcomes respond in high versus low density areas for treated and control individuals. We find

that inventory treatment effects do not significantly differ as a function of treatment intensity for

the pooled treatment.

Effects on net revenues, however, paint a different picture. Treatment effects in low-intensity

areas are much larger – roughly double — those estimated in the pooled specification. This is

because most of the revenue effects seen in the pooled specification are concentrated among treated

individuals in low-intensity sublocations. In contrast, revenue effects for treated individuals in

42 This, along with the overall weaker treatment intensity in Year 2, may contribute to the smaller price effectsobserved in Year 2. In terms of weaker treatment intensity, note that the sample size in Year 2 is only about 65% thatof Year 1. As a result, the intensity in Year 2 is only about 65% what it was in Year 1. Note that the point estimateon “Hi” in column 2 (Y2) of Table 6 is almost exactly 65% of the coefficient on column 1 (Y1). The coefficient on“Hi Intensity * Month” in column 2 (Y2) is close to (a bit more than) 65% of the coefficient on column 1 (Y1).

43Local market effects may not be the only channel through which treatment density affected individual-level results.For example, sharing of maize or informal lending between households could also be affected by the density of loanrecipients. Appendix K explores these alternative channels and presents evidence suggesting that the individual-levelspillover results are most consistent with spillovers through effects on local markets. However, we cannot rule outthat other mechanisms could also be at play.

31

high-intensity sublocations are substantially lower (and, in fact, are statistically indistinguishable

from zero in the pooled results presented Column 6 of Table 7).44,45 Therefore, while individuals

in both high and low-intensity sublocations store significantly more as a result of treatment, only

treated individuals in low-intensity sublocations earn significantly higher revenues. As with earlier

estimates, estimates for consumption remain relatively imprecisely estimated.46,47

Why might loan profitability be lower in high treatment density areas? Intuitively, arbitrage

– the exploitation of price differentials – is most profitable to an individual when she is the only

one arbitraging. As others begin to arbitrage as well, general equilibrium effects drive down these

differentials and therefore diminish the direct returns to arbitrage. Conversely, for those who do

not engage in arbitrage, these spillovers may be positive. Though the timing of their sales will

not change, they may benefit from relatively higher sale prices at harvest-time and relatively lower

purchase prices during the lean season.

We see some evidence of these positive spillovers to control group revenues in high-intensity

treatment areas (see middle panel of Figure 7 and the estimate on the Hi dummy in Column

6 of Table 7). However, it should be noted that this effect is measured with considerable noise

and and thus remains more speculative.48 Given the diffuse nature of spillover effects, it is perhaps

unsurprising that identifying these small effects with statistical precision is challenging.49 However,

they are suggestive of important distributional dynamics for welfare, which we explore below.

44Table 7 displays “p-val T+TH=0,” which indicates the joint significance of β1+β3 from Equation 5; this representsthe full effect of treatment for individuals in high-intensity sublocations.

45While the interaction term “Treat*Hi” is only significant at traditional levels in Year 1, we attribute at leastsome of the weakened Year 2 interaction term to the lower treatment intensity in Year 2. Recall that the sample sizein Year 2 is only about 65% that of Year 1. As a result, the intensity in Year 2 is only about 65% what it was inYear 1. If we scale the coefficient on “Treat*Hi” in Year 2 (column 2) to account for this difference (i.e. divide by0.65), we get an estimate much closer to the Year 1 estimate. In addition, any trader movement that dampened Year2 market-level effects may have further contributed to this weaker Year 2 effect.

46Interestingly, they are strongly positive for treated individuals in the high-intensity areas in Year 2. However,because there is no clear pattern across years, we avoid speculating or over-interpreting this fragile result.

47Because the consumption measure includes expenditure on maize, in Appendix E.1 we also estimate effects onconsumption excluding maize and consumption excluding all food. Results are similar using these measures.

48And even goes in the opposite direction in the Year 2 results alone; see Column 5 of Table 7.49Simple power calculations suggest that if the point estimate of 165 is the true effect, a sample size of 218,668 –

more than 32 times our current sample size – would be necessary to detect this effect with 95% confidence.

32

6.1 Discussion

The randomized saturation design allows us to capture how both direct and indirect treatment

effects vary with saturation level. Table 8 breaks down the distribution of welfare gains from

the loan, based on saturation rate and revenue effects drawn from the pooled results. While this

exercise takes all point estimates as given, note that some are less precisely measured than others.50

As a result, there are likely large standard errors around some of the figures presented in Table 8.

This exercise should therefore be interpreted as an illustration of how general equilibrium effects

can shape the distribution of welfare gains in isolated markets, rather than precise quantitative

estimates.

In the first row, we present the direct gains per household, representing the increase in revenues

driven by treatment for those who are treated (specifically calculated as the coefficient on the

“Treat” dummy in low saturation areas and as the coefficient on the “Treat” dummy plus the

coefficient on the “Treat*Hi” interaction term in high saturation areas). As discussed above, we

see that the direct treatment effects are greater for those in low saturation sublocations, where

treated individuals are closer to “being the only one arbitraging,” than in high saturation areas.

The second row presents the indirect gains per household. This is estimated as zero in low

saturation areas and as the coefficient on “Hi” in high saturation areas.51 We see in row 3 that, in

the high saturation areas, the indirect gains are 58% the size of the direct gains. When we account

for the much larger size of the total population relative to that of just the direct beneficiaries

(presented in rows 5 and 4 respectively), we find that the total size of the indirect gains swamp

that of the direct gains in high saturation areas (rows 7 and 6 respectively).

These findings have two implications. First, the total gains from the intervention (presented in

row 7) are much higher in high saturation areas than they are in low saturation areas. While the

direct gains to the treatment group are lower in areas of high saturation, the small per-household

indirect gains observed in these areas accrue to a large number of untreated individuals, resulting

in an overall increase in total gains (note that although there is a large degree of imprecision in our

50For example, the point estimate on “Treat*Hi” is not quite significant at traditional levels, while the pointestimate on “Hi” is measured with large noise.

51Though note that low-intensity treatment areas may also experience GE effects which we are unable to detect.We are only able to detect relative differences in prices across low- and high-intensity areas.

33

estimate of the indirect gains, the qualitative result that higher saturation produces larger gains

than low saturation holds even at indirect gains as low as 38Ksh/individual, less than $0.5 USD).52

High saturation offers greater relaxation of a barrier to intertemporal trade (credit constraints) and

thereby produces larger aggregate gains.

Second, the distribution of gains shifts in the presence of general equilibrium effects. While in

low saturation areas all of the gains appear to come from direct gains, in high saturation areas,

81% of the total gains are indirect gains (row 9).53 General equilibrium effects therefore more

evenly distribute gains across the entire population, reducing the proportion of the gains that

direct beneficiaries exclusively receive and increasing the share enjoyed by the full population.

This redistribution of gains has implications for private sector investment in arbitrage. Row 10

presents the per-household private gains accruing to arbitragers, as estimated by the coefficient on

the “Treat” indicator in low saturation areas and by the coefficient on the “Treat” dummy plus

the coefficient on the “Treat*Hi” interaction term plus the coefficient on the “Hi” interaction term

in high saturation areas. This represents the per-household gains accruing to treated farmers in

our sample, under each level of saturation. It also represents the most that private sector banks

or other financial institutions could hope to extract from each farmer to whom they might provide

loans for storage. Row 11 presents the total private gains, multiplying the per-household gains by

the number of treated individuals. Despite the fact that high saturation areas have two times the

number of treated farmers, the total private gains are still lower in these areas compared to low

saturation areas.

These calculations suggest that private sector financial institutions may face incentives that

result in the under-provision of finance for arbitrage. Although overall social gains are higher

at greater levels of saturation (row 8), because much of these gains are indirect, private sector

institutions will not be able to capture them. For private sector institutions, the available gains

52Also contributing is the fact that although the direct benefits/household are only a quarter of the size in highareas, there are twice the number of beneficiaries, which makes up some of the gap in terms of total direct gains.

53It is possible that there are general equilibrium effects – and therefore indirect gains – occurring in the lowsaturation areas that we simply cannot detect in the absence of a pure control group. If this is the case, it wouldmean that our current estimates underestimate the total gains, as well as the percentage of gains coming from indirectgains, in low saturation areas. However, it would also mean that we are underestimating these figures in the highintensity areas as well.

34

for capture are actually lower at high levels of saturation (row 11). Row 12 attempts to quantify

this disincentive. At low levels of saturation, private sector institutions could fully internalize all

gains, capturing up to 100% of the total revenue increases generated by the product (under our

assumption of no indirect gains in the low saturation case). However, at high saturation rates, only

31% of the total gains are private. Financial institutions therefore will fail to internalize 69% of

the gains at these higher saturation levels, which will likely result in under-provision of financial

products, compared to the socially optimal level.

7 Conclusion

Large and regular increases in the price of maize between the harvest and the lean season offer

farmers substantial arbitrage opportunities. However, smallholder farmers appear unable to arbi-

trage these price fluctuations due to high harvest-time expenditure needs and an inability to access

credit markets, necessitating high harvest-time sales of maize.

We study the effect of offering Kenyan maize farmers access to a loan during the harvest period.

We find that access to this perhaps counter-intuitively timed credit “frees up” farmers to use storage

to arbitrage these price movements. Farmers offered the loan shift maize purchases into the period of

low prices, put more maize in storage, and sell maize at higher prices later in the season, increasing

farm revenue. Using experimentally-induced variation in the density of treatment farmers across

locations, we document that this change in storage and marketing behavior aggregated across

treatment farmers also affects local maize prices: post harvest prices are significantly higher in

high-density areas, consistent with more supply having been taken off the market in that period,

and are lower later in the season (though not significantly so). These general equilibrium effects

feed back to our profitability estimates, with treatment farmers in low-density areas – where price

differentials were higher and thus arbitrage opportunities greater – differentially benefiting.

The findings make a number of contributions. First, our results are among the few experimental

results to find a positive and significant effect of microcredit on the profits of microenterprises

(farms in our case). This is also to our knowledge one of the first experimental studies to directly

account for general equilibrium effects in this literature. At least in our particular setting, failing to

35

account for these GE effects substantially alters the conclusions drawn about the average benefits

of improved credit access.

This has methodological implications for a broader set of interventions that may shift local

supply – such as agricultural technologies that increase local food supply or vocational training

programs that increase local skilled labor supply – in the presence of thin or imperfectly inte-

grated markets. Our results suggest that, when implemented in rural or fragmented markets, these

interventions may lead local prices to respond substantially enough to alter the profitability of

these interventions for direct beneficiaries and to impact the welfare of non-beneficiaries. Explicit

attention to GE effects in future evaluations is likely warranted.

Finally, we show how the absence of financial intermediation can be doubly painful for poor

households in rural areas. Lack of access to formal credit causes households to turn to much more

expensive ways of moving consumption around in time, and aggregated across households this

behavior generates a large scale price phenomenon that further lowers farm income and increases

what most households must pay for food. The results suggest that expanding access to affordable

credit could reduce this price variability and thus have benefits for recipient and non-recipient

households alike. Welfare estimates in our setting suggest that a large portion of the benefits of

expanded loan access could accrue indirectly to non-borrowers. Under such a distribution of welfare

gains, private sector financial institutions may undersupply credit relative to the social optimum,

raising the possibility that public credit programs could raise aggregate welfare.

What our results do not address is why wealthy local actors – e.g. large-scale private traders

– have not stepped in to bid away these arbitrage opportunities. Traders do exist in the area and

can commonly be found in local markets. In a panel survey of local traders in the area, we record

data on the timing of their marketing activities and storage behavior. But we find little evidence

of long-run storage. When asked to explain this limited storage, many traders report being able to

make even higher total profits by engaging in spatial arbitrage across markets (relative to temporal

arbitrage). Nevertheless, this does not explain why the scale or number of traders engaging in both

spatial and intertemporal arbitrage has not expanded; imperfect competition among traders may

play a role (Bergquist, 2017).

36

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that

the

min

imu

mm

onth

lyp

rice

=100.

Ou

rst

ud

ysi

tein

wes

tern

Ken

ya

issh

own

ingr

een

,an

dth

eb

lue

squ

ares

rep

rese

nt

anin

dep

end

ent

esti

mate

of

the

month

sof

the

mai

nh

arve

stse

ason

inth

egi

ven

loca

tion

.P

rice

flu

ctu

atio

ns

for

mai

ze(c

orn

)in

the

US

are

show

nin

the

low

erle

ftfo

rco

mp

ari

son

●

●

●

●●

●

●

100

105

110

115

120

Aru

sha

IndexJa

nM

arM

ayJu

lSe

pN

ov

100

105

110

115

120

125

Kam

pala

Index

Jan

Mar

May

Jul

Sep

Nov

100

105

110

115

Kig

ali

Index

Jan

Mar

May

Jul

Sep

Nov

100

105

110

115

120

125

Kis

umu

Index

Jan

Mar

May

Jul

Sep

Nov

100

110

120

130

140

150

Mbe

ya

Index

Jan

Mar

May

Jul

Sep

Nov

100

105

110

115

120

125

130

Eldo

ret

Index

Jan

Mar

May

Jul

Sep

Nov

Stud

y si

te

100

105

110

115

120

US

corn

Index

Jan

Mar

May

Jul

Sep

Nov

Mai

n m

aize

ha

rves

t

Keny

aU

gand

a Tanz

ania

Rwan

da

Buru

ndi

41

Fig

ure

2:S

tud

yd

esi

gn

.R

and

omiz

atio

nocc

urs

atth

ree

leve

ls.

Fir

st,

trea

tmen

tin

ten

sity

was

ran

dom

ized

acr

oss

17

sub

loca

tion

s(t

ople

vel,

each

box

rep

rese

nts

asu

blo

cati

on).

Th

isra

nd

omiz

atio

nw

ash

eld

con

stan

tac

ross

the

two

years

.S

econ

d,

trea

tmen

tw

as

ran

dom

ized

atth

egr

oup

level

wit

hin

sub

loca

tion

s(s

econ

dle

vel,

each

box

rep

rese

nti

ng

agro

up

ina

giv

ensu

blo

cati

on

).In

Yea

r1,

trea

tmen

tgr

oup

sw

ere

furt

her

div

ided

into

Oct

ober

and

Jan

uar

ylo

ans.

InY

ear

2,on

lyon

eti

min

gof

the

loan

was

off

ered

(in

Nov

emb

er).

Fin

ally

,in

Yea

r1,

ther

ew

asa

thir

dle

vel

ofra

nd

omiz

atio

nat

the

indiv

idu

al

leve

l,in

wh

ich

the

tags

an

dlo

ckb

oxw

ere

cros

s-ra

nd

omiz

ed(b

otto

mle

vel)

.In

Yea

r2,

no

ind

ivid

ual

leve

ltr

eatm

ents

wer

eoff

ered

.T

ota

lnu

mb

ers

of

ran

dom

ized

un

its

inea

chb

inar

egi

ven

onth

ele

ft. Y

ear

1

7

Laur

en s

crat

ch_v

1 BO

S

c

Hig

h in

tens

ity

Low

inte

nsity

Trea

tmen

t Con

trol

Oct

(T1

) Ja

n (T

2)

Su

blo

cati

on-l

evel

ra

nd

omiz

atio

n

Hig

h in

tens

ity =

9 lo

catio

ns

Low

inte

nsity

= 8

loca

tions

Gro

up

-lev

el

ran

dom

izat

ion

T1

= 7

9 gr

oups

T2

= 8

0 gr

oups

C =

81

grou

ps

Loan

+

Tag

s

Loan

+

Tags

+

Lock

box

Loan

+

Tag

s

Loan

+

Tags

+

Lock

box

Not

hing

Ta

gs

Lock

box

Ind

ivid

ual

-lev

el

ran

dom

izat

ion

Trea

tmen

t Con

trol

Oct

(T1

) Ja

n (T

2)

Loan

+

Tag

s

Loan

+

Tags

+

Lock

box

Loan

+

Tag

s

Loan

+

Tags

+

Lock

box

Not

hing

Ta

gs

Lock

box

Yea

r2

8

Laur

en s

crat

ch_v

1 BO

S

c

Hig

h in

tens

ity

Low

inte

nsity

Trea

tmen

t (N

ov)

Con

trol

Su

blo

cati

on-l

evel

ra

nd

omiz

atio

n

Hig

h in

tens

ity =

9 lo

catio

ns

Low

inte

nsity

= 8

loca

tions

Gro

up

-lev

el

ran

dom

izat

ion

T

= 8

5 gr

oups

C =

86

grou

ps

Trea

tmen

t (N

ov)

Con

trol

Re-

ran

dom

ize:

42

Figure 3: Study timeline. The timing of the interventions and data collection are show. Year 1spanned 2012-2013, Year 2 spanned 2013-2014, and the long-run follow-up data collection occurred2014-2015. The market survey, shown in red, ran from November 2012-December 2015. The baselinewas run August-September 2012. Three rounds of household data were collected on a rolling basisin each year of the main study. A long-run follow-up survey was run September-December 2015.Light blue arrows show the timing of the loan announcement (immediately as harvest was ending),while dark blue arrows display the date of loan disbursal (October and January in Year 1, Novemberin Year 2). Harvest time is highlighted in grey and occurs in September-October each year.

A S O N D J F M A M J J A

2012 2013

S O N D J F M A M J J A S O

2013 2014

Year1(2012-13)

Year2(2013-14)

Baseline Round1 Round2 Round3

Marketsurvey

Round1 Round2 Round3

Marketsurvey

N D J F M A M J J A S O N D

2014 2015

LRFU(2014-15)

Long-RunFollow-Up

Marketsurvey

HarvestHouseholdsurveyMarketsurvey Loandisbursed Loanannounced

43

Figure 4: Panel A: Maize price trends (pre-study period). Farmer-reported average monthlymaize prices for the period 2007-2012, averaged over all farmers in our sample. Prices are in Kenyanshillings per goro (2.2kg). Panel B: Maize price trends (study period & post-study period).Author-collected average monthly maize prices for the period 2012-2014 (study period) and 2014-2015 (post study period), averaged over all markets in our sample. Prices are in Kenyan shillingsper goro (2.2kg).

Panel A

6070

8090

100

110

pric

e (K

SH/g

oro)

Sep Oct Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Panel B

5060

7080

90Pr

ice

(Ksh

/gor

o)Sep Oct Nov Dec Jan Feb Mar Apr May Jun Jul Aug

2012-2013 2013-20142014-2015

Figure 5: Pooled Treatment effects. The top row of plots shows how average inventories, netrevenues, and log household consumption evolve from December to August in Y1 and Y2 (pooled)in the treatment group versus the control group, as estimated with fan regressions. The bottomrow shows the difference between the treatment and control, with the bootstrapped 95% confidenceinterval shown in grey (100 replications drawing groups with replacement).

02

46

8In

vent

ory

(90k

g ba

gs)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Control Treatment

Inventories

-300

0-1

000

1000

3000

Net

Rev

enue

s (K

SH)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Control Treatment

Net revenues

9.2

9.3

9.4

9.5

9.6

Tota

l HH

con

sum

ptio

n (lo

g)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Control Treatment

Household consumption

-20

24

Inve

ntor

ies,

T -

C

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Pt Est 95% CI 90% CI

Inventories

-400

0-2

000

020

0040

00N

et R

even

ues,

T -

C

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Pt Est 95% CI 90% CI

Net Revenues

-.4-.2

0.2

.4To

tal H

H c

onsu

mpt

ion

(log)

, T -

C

Nov Dec Jan Feb Mar Apr May Jun Jul Aug

Pt Est 95% CI 90% CI

Total HH consumption (log)

44

Figure 6: Pooled market prices for maize as a function of local treatment intensity.Markets matched to treatment intensity using sublocation of the modal farmer within 3km of eachmarket. The left panel shows the average sales price in markets in high-intensity areas (solid line)versus in low-intensity areas (dashed line) over the study period. The middle panel shows the aver-age difference in log price between high- and low-intensity areas over time, with the bootstrapped95% confidence interval shown in light grey and the 90% confidence interval shown in dark grey.The right panel shows the robustness of results to alternative radii (1km, 3km, and 5km)

5560

6570

7580

Pric

e (K

sh/g

oro)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug Sep

Lo Hi -7-5

-3-1

13

57

Diff

eren

ce in

pric

e (%

)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug Sep

Pt Est 95% CI 90% CI -7-5

-3-1

13

57

Diff

eren

ce in

pric

e (%

)

Nov Dec Jan Feb Mar Apr May Jun Jul Aug Sep

1km 3km 5km

Figure 7: Pooled Treatment effects by treatment intensity. Average inventories, net rev-enues, and log HH consumption over the study period in the treatment group versus the controlgroup, split apart by high intensity areas (orange lines) and low-intensity areas (black lines).

02

46

inve

ntor

y (b

ags)

Dec Jan Feb Mar Apr May Jun Jul Aug

T Hi T Lo C Hi C Lo

Inventories

-600

0-4

000

-200

00

2000

Net

reve

nues

(KSH

)

Dec Jan Feb Mar Apr May Jun Jul Aug

T Hi T Lo C Hi C Lo

Net revenues

8.8

99.

29.

49.

69.

8lo

g KS

H

Dec Jan Feb Mar Apr May Jun Jul Aug

T Hi T Lo C Hi C Lo

HH cons.

45

Table 1: Summary statistics and balance among baseline covariates. Balance table forthe Y1 study (restricted to the Y1 sample, for which we have baseline characteristics. The firsttwo columns give the means in each treatment arm. The 3rd column gives the total number ofobservations across the two groups. The last two columns give differences in means normalized bythe Control sd, with the corresponding p-value on the test of equality.

Baseline characteristic Treat Control Obs T - Cstd diff p-val

Male 0.30 0.33 1,589 -0.08 0.11Number of adults 3.00 3.20 1,510 -0.09 0.06Kids in school 3.00 3.07 1,589 -0.04 0.46Finished primary 0.72 0.77 1,490 -0.13 0.02Finished secondary 0.25 0.27 1,490 -0.04 0.46Total cropland (acres) 2.44 2.40 1,512 0.01 0.79Number of rooms in hhold 3.07 3.25 1,511 -0.05 0.17Total school fees (1000 Ksh) 27.24 29.81 1,589 -0.06 0.18Average monthly cons (Ksh) 14,970.86 15,371.38 1,437 -0.03 0.55Avg monthly cons./cap (log Ksh) 7.97 7.96 1,434 0.02 0.72Total cash savings (KSH) 5,157.40 8,021.50 1,572 -0.09 0.01Total cash savings (trim) 4,731.62 5,389.84 1,572 -0.05 0.33Has bank savings acct 0.42 0.43 1,589 -0.01 0.82Taken bank loan 0.08 0.08 1,589 -0.02 0.73Taken informal loan 0.24 0.25 1,589 -0.01 0.84Liquid wealth 93,878.93 97,280.92 1,491 -0.03 0.55Off-farm wages (Ksh) 3,916.82 3,797.48 1,589 0.01 0.85Business profit (Ksh) 2,302.59 1,801.69 1,589 0.08 0.32Avg %∆ price Sep-Jun 133.49 133.18 1,504 0.00 0.94Expect 2011 LR harvest (bags) 9.36 9.03 1,511 0.02 0.67Net revenue 2011 -3,303.69 -4,088.62 1,428 0.03 0.75Net seller 2011 0.32 0.30 1,428 0.05 0.39Autarkic 2011 0.07 0.06 1,589 0.03 0.51% maize lost 2011 0.02 0.01 1,428 0.03 0.572012 LR harvest (bags) 11.18 11.03 1,484 0.02 0.74Calculated interest correctly 0.71 0.73 1,580 -0.03 0.50Digit span recall 4.57 4.58 1,504 -0.01 0.89Maize giver 0.26 0.26 1,589 -0.00 0.99

“Liquid wealth” is the sum of cash savings and assets that could be easily sold (e.g. livestock). Off-farm wages andbusiness profit refer to values over the previous month. Net revenue, net seller, and autarkic refer to the household’smaize marketing position. “Maize giver” is whether the household reported giving away more maize in gifts than itreceived over the previous 3 months.

46

Tab

le2:

Invento

ryE

ffects

,In

div

idu

al

Level.

Reg

ress

ion

sin

clu

de

rou

nd

-yea

rfi

xed

effec

ts,

wit

her

rors

clu

ster

edat

the

gro

up

leve

l.

Y1

Y2

Poole

d

(1)

(2)

(3)

(4)

(5)

(6)

Ove

rall

By

rdO

ver

all

By

rdO

vera

llB

yrd

Tre

at0.

52∗∗

∗0.

50∗∗

∗0.5

3∗∗∗

(0.1

6)(0

.14)

(0.1

2)

Tre

at-

R1

0.82

∗∗∗

1.21∗

∗∗1.0

3∗∗∗

(0.3

1)(0

.24)

(0.2

0)

Tre

at-

R2

0.71

∗∗∗

0.24

0.5

2∗∗

∗

(0.1

9)(0

.15)

(0.1

2)

Tre

at-

R3

0.06

0.04

0.0

7(0

.07)

(0.3

7)

(0.1

9)

Ob

serv

atio

ns

3836

3836

2944

2944

6780

6780

Mea

nD

V2.

672.

671.

681.

68

2.1

62.1

6R

squ

ared

0.35

0.35

0.18

0.19

0.2

90.3

0

47

Tab

le3:

Net

Revenu

eE

ffects

,In

div

idu

al

Level.

Reg

ress

ion

sin

clu

de

rou

nd

-yea

rfixed

effec

ts,

wit

her

rors

clust

ered

at

the

grou

ple

vel.

Y1

Y2

Poole

d

(1)

(2)

(3)

(4)

(5)

(6)

Ove

rall

By

rdO

ver

all

By

rdO

ver

all

By

rd

Tre

at27

9.78

800.

24∗∗

524.6

6∗∗

(292

.16)

(330

.63)

(220.2

5)

Tre

at-

R1

-114

6.56

∗∗∗

-23.

71

-608.6

8∗∗

(325

.13)

(478

.41)

(285.7

0)

Tre

at-

R2

534.

8519

17.2

8∗∗

∗1170.7

1∗∗

∗

(485

.80)

(532

.81)

(359.8

4)

Tre

at-

R3

1371

.95∗∗

∗52

0.76

985.7

9∗∗∗

(436

.12)

(403

.27)

(302.0

9)

Ob

serv

atio

ns

3795

3795

2935

2935

6730

6730

Mea

nD

V33

4.41

334.

41-3

434.

38-3

434.3

8-1

616.1

2-1

616.1

2R

squ

ared

0.01

0.01

0.04

0.05

0.0

90.0

9

48

Tab

le4:

HH

Con

sum

pti

on

(log)

Eff

ects

,In

div

idu

alL

evel.

Reg

ress

ion

sin

clu

de

rou

nd

-yea

rfi

xed

effec

ts,

wit

her

rors

clu

ster

edat

the

grou

ple

vel.

Y1

Y2

Poole

d

(1)

(2)

(3)

(4)

(5)

(6)

Ove

rall

By

rdO

vera

llB

yrd

Ove

rall

By

rd

Tre

at0.

000.

07∗

0.0

4(0

.03)

(0.0

4)(0

.03)

Tre

at-

R1

-0.0

40.0

70.0

1(0

.05)

(0.0

5)

(0.0

3)

Tre

at-

R2

0.02

0.08∗

0.0

5(0

.04)

(0.0

5)

(0.0

3)

Tre

at-

R3

0.03

0.0

60.0

4(0

.05)

(0.0

5)

(0.0

3)

Ob

serv

atio

ns

3792

3792

2944

2944

6736

6736

Mea

nD

V9.

489.

489.

619.

61

9.5

59.5

5R

squ

ared

0.00

0.00

0.01

0.01

0.0

20.0

2

49

Table 5: Net Sales and Effective Prices, Individual Level. Columns 1-2 regressions onnet sales (quantity sold minus quantity purchased) include round-year fixed effects, with errorsclustered at the group level. Columns 3-4 include only one observation per individual (per year).Round fixed effects are omitted in these specifications in order to estimate the effect of treatmenton prices paid and received, which change because of shifts in the timing of transactions; thereforeround controls are not appropriate. “Effective purchase price” is constructed by the dividing thetotal value of all purchases over the full year (summed across rounds) by the total quantity of allpurchases over the full year. “Effective sales price” is constructed similarly.

Net Sales Effective Price

Overall By rd Purchase Sales

Treat 0.12∗ -104.94∗∗∗ 131.70∗∗∗

(0.06) (31.57) (40.85)

Treat - R1 -0.26∗∗

(0.10)

Treat - R2 0.27∗∗∗

(0.10)

Treat - R3 0.29∗∗∗

(0.09)

Observations 6108 6108 2014 1428Mean DV -0.62 -0.62 3084.78 2809.76R squared 0.16 0.16 0.01 0.01

50

Table 6: Market prices for maize as a function of local treatment intensity. “Hi” intensityis a dummy for a sublocation randomly assigned a high number of treatment groups. “Month” isa linear month time trend (beginning in Nov at 0 in each year). Standard errors are clustered atthe sublocation level. Prices measured monthly following loan disbursal (Nov-Aug in Y1; Dec-Augin Y2). Price normalized to 100 in Nov in low-intensity sublocations.

Main Specification (3km) Robustness (Pooled)

Y1 Y2 Pooled 1km 5km

Hi 4.41∗ 2.85 3.97∗∗ 2.79 3.77∗

(2.09) (1.99) (1.82) (1.72) (1.82)

Month 1.19∗∗∗ 1.22∗∗∗ 1.36∗∗∗ 1.33∗∗∗ 1.54∗∗∗

(0.36) (0.38) (0.35) (0.34) (0.29)

Hi Intensity * Month -0.57 -0.48 -0.57 -0.52 -0.83∗∗

(0.42) (0.46) (0.39) (0.39) (0.37)

Observations 491 381 872 872 872R squared 0.08 0.03 0.06 0.06 0.06

51

Tab

le7:

Invento

ry,

Net

Revenu

es,

an

dH

HC

on

sum

pti

on

(log)

Eff

ects

,A

ccou

nti

ng

for

Tre

atm

ent

Inte

nsi

ty.

Re-

gres

sion

sin

clu

de

rou

nd

-yea

rfi

xed

effec

tsw

ith

erro

rscl

ust

ered

atth

esu

blo

cati

onle

vel.

P-v

alu

eson

the

test

that

the

sum

of

the

Tre

atan

dT

reat

*Hi

equ

alze

roar

ep

rovid

edin

the

bot

tom

row

sof

the

tab

le.

Inve

nto

ryN

etR

even

ues

Con

sum

pti

on

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

Y1

Y2

Pool

edY

1Y

2P

oole

dY

1Y

2P

oole

d

Tre

at0.

76∗∗

∗0.

55∗∗

∗0.

74∗∗

∗10

59.6

0∗∗

1193

.77

1101.3

9∗∗

0.0

1-0

.05

-0.0

1(0

.19)

(0.1

8)(0

.15)

(437

.73)

(685

.05)

(430.0

9)

(0.0

4)

(0.0

4)

(0.0

2)

Hi

0.12

-0.0

30.

0253

3.90

-152

.60

164.9

4-0

.00

-0.0

8-0

.05

(0.3

6)(0

.22)

(0.2

4)(5

51.1

8)(5

58.9

5)(4

79.6

8)

(0.0

5)

(0.0

5)

(0.0

4)

Tre

at*H

i-0

.33

-0.0

7-0

.29

-111

4.63

∗-5

55.2

1-8

16.7

7-0

.01

0.1

7∗∗

∗0.0

7∗

(0.2

3)(0

.25)

(0.1

9)(5

35.5

9)(8

04.8

6)(5

20.0

4)

(0.0

5)

(0.0

6)

(0.0

4)

Ob

serv

atio

ns

3836

2944

6780

3795

2935

6730

3792

2944

6736

Mea

nD

V2.

741.

382.

04-2

53.5

1-3

620.

40-1

980.0

29.4

79.6

59.5

6R

squ

ared

0.35

0.18

0.29

0.01

0.04

0.0

90.0

00.0

20.0

3p

-val

T+

TH

=0

0.01

0.02

0.01

0.86

0.15

0.4

10.9

70.0

10.0

8

52

Table 8: Distribution of gains in the presence of general equilibrium effects Calculationsemploy per-round point estimates on revenues β1, β2, and β2 (estimated in Ksh) from Column 6 ofTable 7 (multiplied by three to get the annual revenue gains). Direct gains per household (row 1)are calculated as the coefficient on the “Treat” dummy in low saturation areas and as the coefficienton the “Treat” dummy plus the coefficient on the “Treat*Hi” interaction term in high saturationareas). Indirect gains per household (row 2) are estimated as zero in low saturation areas and as thecoefficient on “Hi” in high saturation areas. The total gains from the intervention (row 7) includethe direct gains that accrue to borrowers (row 1) and the indirect gains generated by GE effects(row 2). In high saturation areas, 81% of the total gains are indirect gains (row 9). The privategains per household are estimated by the coefficient on the “Treat” indicator in low saturation areasand by the coefficient on the “Treat” dummy plus the coefficient on the “Treat*Hi” interaction termplus the coefficient on the “Hi” interaction term in high saturation areas. Row 11 presents the totalprivate gains, multiplying the per-person gains by the number of treated individuals. Additionalassumptions and calculation details are laid out in Appendix M. Note that while the private gainsare greater at low saturation, the total gains are greater at high saturation.

Low Saturation High Saturation

1. Direct gains/HH 3,304 854

2. Indirect gains/HH 0 495

3. Ratio of indirect to direct gains 0.00 0.58

4. Direct beneficiary population (HH) 247 495

5. Total local population (HH) 3,553 3,553

6. Total direct gains 816,984 422,248

7. Total indirect gains 0 1,757,880

8. Total gains (direct + indirect) 816,984 2,180,128

9. Fraction of gains indirect 0.00 0.81

10. Private gains/HH 3,304 1,349

11. Total private gains 816,984 666,945

12. Fraction of gains private 1.00 0.31

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